Tackling Social Exclusion: Evidence from Chile

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Department of Economics

Working Paper 2014:3

Tackling Social Exclusion: Evidence from Chile

Pedro Carneiro, Emanuela Galasso and

Rita Ginja

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Department of Economics Working paper 2014:3

Uppsala University May 2014

P.O. Box 513 ISSN 1653-6975

SE-751 20 Uppsala Sweden

Fax: +46 18 471 14 78

Tackling Social Exclusion: Evidence from Chile

Pedro Carneiro, Emanuela Galasso and Rita Ginja

Papers in the Working Paper Series are published on internet in PDF formats.

Download from http://www.nek.uu.se or from S-WoPEC http://swopec.hhs.se/uunewp/

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Tackling Social Exclusion: Evidence from Chile

Pedro Carneiro

^∗

Emanuela Galasso

^†

Rita Ginja

^‡§

May 9, 2014

Abstract

We study an innovative welfare program in Chile which combines a period of frequent home visits to households in extreme poverty, with guaranteed access to social services. Program impacts are identified using a regression discontinuity design, exploring the fact that program eligibility is a discontinuous function of an index of family income and assets. We find strong and lasting impacts of the program on the take up of subsidies and employment services.

These impacts are important only for families who had little access to the welfare system prior to the intervention.

Keywords: Social Exclusion, Social Protection, Chile, Extreme Poverty JEL Codes: C26, I38, J08

∗University College London, CEMMAP, IFS. Email:p.carneiro@ucl.ac.uk

†World Bank. Email: egalasso@worldbank.org

‡Uppsala University and Uppsala Center for Labor Studies. Email: rita.ginja@nek.uu.se

§The authors are grateful to the Executive Secretary at the Ministry of Planning (now Ministry of Social Development) and FOSIS for granting access to the data used in this paper. We gratefully acknowledge the generous financial support of the Research Budget Committee of the World Bank (RSB), the Spanish Trust Fund for Impact Evaluation (SIEF) and the World Bank Gender Action Plan. Rita Ginja acknowledges the financial support from the Funda¸c˜ao para a Ciˆencia e Tecnologia and the Royal Economic Society. Pedro Carneiro gratefully acknowledges the financial support from the Economic and Social Research Council (grant reference RES-589-28-0001) through the Centre for Microdata Methods and Practice), the support of the European Research Council through ERC- 2009-StG-240910-ROMETA and ERC-2009 Advanced Grant 249612. We thank the comments of participants at the Econometric Society Winter Meetings 2010, NEUDC 2011, 2011 World Bank CCT 2nd Generation Conference, LACEA 2011, IZA-World Bank Conference 2013, SESP-Northwestern and AEA Meetings 2014. We are indebted to Theresa Jones for her support in the evaluation effort and to Veronica Silva for sharing her knowledge about the design of the programs under study. These are the views of the authors and do not reflect those of the World Bank, its Executive Directors, or the countries they represent. All errors are our own.

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1 Introduction

Households in extreme poverty are generally deprived in multiple dimensions. The lack of material resources, coupled with little access to information, and other constraints to their decision making ability (Mullainathan and Shafir, 2013), limit the actions they can take towards improving their lives (Bertrand et al., 2006, Duflo, 2012). Although this is well known, most anti-poverty programs address single aspects in isolation of all other ones, and focus mainly on the lack of financial resources.

In 2002, Chile implemented Chile Solidario (CS hereafter), an anti-poverty program which was progressive by the standards of most countries, even in the developed world. The target of the program were the 5% poorest families in Chile, who were perceived not only to be poor, but also alienated from the welfare services potentially available to them. The program simultaneously tackled multiple dimensions of deprivation in the lives of these families through frequent and per- sonal contact with them, and the coordination of different government agencies providing various social services. Many other Latin American countries began looking at this system of integrated social services as an example for their own policies, and a few of them introduced programs that mimic several aspects of CS (such as Juntos/Unidos in Colombia, or Brasil Sem Mis´eria in Brazil).

This paper studies short and medium run impacts of CS on those who participated in it between 2002 and 2006. Our main results focus on three sets of outcomes: the take-up of subsidies, and participation in training and employment programs; the labor force participation and employment of heads of household and their spouses; and housing conditions.¹ We find that CS participants increase their take-up of a family allowance for poor children (the Subsidio Unico Familiar, hereafter SUF) by 11%, relatively to an average take-up of 65% among comparable non-participants. There is also some impact on the uptake of employment programs, of about 5-6% (from a baseline enrolment of 1%), especially in the short run. However, this is not accompanied by general improvements in employment outcomes. Finally, we find no evidence of important impacts on housing conditions of participant families.

Program impacts on the take-up of subsidies are especially large for families not accessing services before CS was implemented (the primary target group), and for families enrolling in CS only after 2004, when the expansion of the supply of social services was effectively implemented.

For example, the increase in the uptake of SUF is 22% for families who did not take up these subsidies before 2002, and it is visible at least for 4 years after the family first enrolled in CS.

If we further condition on having enrolled in CS after 2004, the impact on the take-up of SUF rises to 32%.² Similarly, there is a 20% increase in the employment rate of females (spouses of the

1The choice of outcomes is dictated in part by the fact that we use administrative data in our evaluation, which has a more limited set of outcomes than, say, a household survey. The benefit of using administrative records is that we can study the universe of participants in the welfare system, as opposed to a small sample of them.

2Since the baseline take-up of SUF is 65%, this means a change towards nearly universal coverage of this subsidy among eligible families registered in the social welfare system.

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household head), if they were not employed before 2002, and if their family enroled in CS after 2004.

In order to evaluate the program we use a regression discontinuity design. Families are eligible to participate in CS if a poverty index is below a given threshold, which varies across municipalities and across years. Thus we compare, within municipality and cohort, the outcomes of families who are just eligible with the outcomes of those who are just ineligible for the program.

The discontinuity in the probability of participation in CS induced by the poverty index is not sharp but fuzzy, since not all families identified as target of the program in 2001 were immediately served. This happened mainly because of supply constraints. CS was rolled out for a period of 5 years and about 20% of the 250,000 target families were enrolled each year, giving priority to the poorest (more than 95% of all eligible families invited to participate in CS accept the invitation).

We estimate that the average impact of eligibility for CS on participation in the program is about 21% (for households with a poverty index in the neighborhood of the discontinuity). We then produce intention to treat (ITT) and instrumental variables (IV) estimates of the impact of CS, using eligibility to CS as an instrument for participation in the program. We use administrative records that cover a period of 10 years (2000-2009). We start observing families at least a year before the introduction of CS, and we follow them up to 6 years after entry into the program.

Galasso (2006) conducts the first evaluation of this program. She uses a household survey that was specifically collected for the evaluation of this program, and two empirical methods, namely matching on the propensity score, and a regression discontinuity procedure analogous to the one used in our paper. She finds that the program induced significant impacts on the education and health of households, and the take-up of social benefits. This last results is consistent with the findings in this paper, whereas the administrative data we use does not allow us to analyze either health or education outcomes in detail. However, the survey she uses was designed for the use of a matching estimator, and it is neither particularly suitable nor large enough for a credible implementation of her RD estimator. Our ability to use administrative records for the whole population of welfare recipients in Chile is a substantial improvement over the data used in her paper if the goal is to rely on an RD type estimator. The cost of using this data is that the set of outcomes that we can possibly observe is much smaller. Larra˜naga, Contreras and Ruiz Tagle (2009) and Hoces, Hojman and Larra˜naga (2011) were developed contemporaneously with our paper. They use exactly the same administrative dataset as us, although in the latter paper they also complement it with the household survey originally used in Galasso (2006). The questions they ask are analogous to ours, but the evaluation methodology is quite different. They rely on a mix of differences in differences and matching, and find small impacts of the program across a variety of dimensions. They also focus on more limited set of cohorts than we do.

The RD estimator we use here provides an important alternative to evaluation results based on the matching or differences in differences estimators implemented in the papers discussed above.

Relatively to the matching estimator, it accounts for selection into the program based on unobserv-

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able variables. Relatively to a differences in differences estimator, it does not rely on a common trends assumption between treatment and control groups, which may be problematic if the poorest households in Chile, which are also the first to be served by the program, are on a different trend than those not served by the program, which could well be the case. The standard criticism of an RD type estimator such as the one we implement is that it is only able to identify program impacts for the population of households in the neighborhood of the discontinuity threshold, which may or may not be an interesting parameter to look at, depending on the application. However, in our setting there is a very large number thresholds, which vary across time and space, which means that we are able to identify program impacts in the neighborhood of a large number of discontinuity points. Therefore, while it is still true that we will not be able to estimate program impacts for very poor and very rich people, who are never in the neighborhood of any of the discontinuities considered here, our estimates should be valid for a large set of households in the middle of these two groups. Sarsoza and Urzua (2012) also study this program using the RD strategy introduced in Galasso (2006) and refined in this paper, and similar administrative records. However, their focus is very different: their outcome of interest is test scores of children, which can be obtained from school records and merged with program records. In addition, they study only the first cohort of participants. This could be a limitation since the program is likely to have become much more effective for later cohorts, as we explain below. In their paper, they report not only the average impact of the program from the RD estimator, but also how these impacts vary across different discontinuity thresholds.

CS is a program of general interest because it is a serious attempt to integrate several welfare services to tackle social exclusion, and because of its success in connecting the most disadvantaged families in society to the welfare system in a sustained way. The central ideas behind a program such as CS are stressed in Banerjee and Duflo (2007) and in Duflo’s (2012) Tanner lectures. The increase in access to monetary subsidies and services for households previously disconnected from the welfare system is not only important because families are able to supplement their income through them, but also because they become more linked to the social protection system. The intense psychosocial support through home visits is central to help households acquire the skills they need to autonomously participate in (and benefit from) the welfare, education and health systems available to them.

However, even a program as innovative and intensive such as CS is not able to transform the lives of the poorest families along key long term welfare outcomes, such as employment and housing. The target population is difficult to work in terms of skills, and physical capital and psychological endowments. The large theoretical literature on poverty traps shows how tackling both capital and skills constraints can alter the poor’s occupational choices and make them exit poverty (Banerjee and Newman, 1993, Besley, 1995, Banerjee and Duflo, 2007). A more recent literature has also focused on psychological constraints (Mullainathan and Shafir, 2013).

The empirical evidence on interventions that combine capital and skill enhancement in devel-

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oping countries is small but growing rapidly. Integrated programs for poor adolescents (Bandiera et al., 2012), or for the extreme poor (Bandiera et al., 2013, and Duflo and Banerjee 2013), can have transformational effects on their employment and income trajectories when they are of very high quality. In most countries, as in Chile, such programs are responsibility of the welfare system.

Therefore, even if the frequent home visits provided by a program such as CS help diagnose the needs of each family, and stimulate their demand for social services, the extent to which their lives can improve depends on the quality of the programs that are made available to them, and the extent to which these programs are tailored to their needs.³

The paper proceeds as follows. In the next section we describe the program. In Section 3 we explain the empirical strategy; Section 4 describes the data. In Section 5 we present and discuss our results. Section 6 concludes.

2 Chile Solidario

CS was designed by the Chilean Government to reach the families who lived in extreme poverty in 2002. The mechanism of targeting and the structure of CS changed substantially in 2006, therefore our study focuses on the first five cohorts of entrants (2002-2006). The program is unique in that it recognizes that the provision of financial resources is not a sufficient condition for alleviating extreme poverty, since families in extreme poverty face multiple other constraints, starting with their inability to use the available welfare services. CS promotes the demand for social services through home visits and by offering preferential access to these services. On the institutions’ side, CS promotes the coordination of different social services at the local level for a more effective targeting of the neediest families. We now provide more detail on the most important aspects of the program.

Home visits The home visiting component of CS lasts for 24 months. It consists of a total of 21 home visits of 40-45 minutes, with the interval between visits increasing over time. The visits are done by social workers, who make the link between families and the network of public and private services available to families. Each year, a social worker is responsible for 50 families on average (SD 25).

The home visiting period has 2 phases: the initial 6-8 months is a period of intensive work between families and counselor and the final 16-18 months are a follow-up period. During these

3Colombia introduced in 2007 a program similar to CS (Juntos), but which unfortunately suffered from a number of implementation and data problems, limiting the comparison we can make with our study (see Econometria, 2011).

This is especially unfortunate because, unlike CS (for which we must rely on quasi-experimental of evaluation), the evaluation of Juntos had originally an experimental design. However, during the evaluation period there was incomplete treatment with most families receiving at most 6 home visits (instead of the 20 originally expected), so only a very weak version of the program could be studied. In addition, social workers had a caseload that was much heavier than that of CS. Finally, although households were encouraged to take-up social services, in many cases such services were not available to them.

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home visits the social worker and families agree to fulfil 53 minimum conditions (see table A.1).

The direct cost of home visits (including the cost of the visit itself, and the training of social worker, and supervision) amounts on average to USD$263 per family over the two years of in which these visits take place.

Guaranteed access to monetary subsidies Participating families receive a monthly cash transfer (called Bono Chile Solidario) during the first 24 months, with the size of the transfer ranging between USD$8 and USD$21 per month (decreasing over time).⁴ For the subsequent three years, families receive the Bono de Engreso (exit grant), which amounts to roughly $8 per month. The transfer is uniform across families. The amount of the CS transfer is much lower than that of other well known conditional cash transfers in Latin America. The goal of the monthly transfer is to compensate families for the costs of participating in the program, instead of consisting of a subsistence transfer, as in other CCT.⁵

Families in CS are guaranteed access to a monthly (non-contributory) allowance for poor families with children less than 18 years of age (SUF - Subsidio Unico Familiar ); the pension for the elderly poor, for the disabled, and for individuals with mental disabilities (PASIS - Pension Asistencial ); and the water subsidy (SAP - Subsidio de Agua Potable), which covers the water bills for up to 15 cubic meters of monthly consumption.

Preferential access to social services and the reorganization of the supply side Par- ticipating families have preferential access to a whole array of social services locally available in municipality of residence. Employment and training programs are of particular interest due to their potential effects on individuals’ labor market outcomes. These programs fall into three cate- gories: (i) job placement programs for wage employment, mainly job training programs and wage subsidies (ii) self-employment programs and support to micro-enterprizes, through a combination of technical assistance and seed funding for inputs and startup capital, and (iii) employability programs, which range from adult education equivalency and training focused on soft-skills. The employment and training programs available are described in table A.2 in the Appendix A.

Although families started receiving visits from social workers in 2002, the first cohorts of beneficiaries had to rely on the existing supply of services available in each municipality. Municipalities and local services providers were simply asked to improve the coordination of different programs serving the target population. After 2004 (when the law governing CS was passed), there was an improvement in the quantity and quality of the supply of such auxiliary services. The programs

4The amount of the Bono is: $21 per month for the first 6 months, $16 per month between month 7-12, $11 per month for months 13-18, and $8 for the last 6 months. These amounts are for 2006 but they are adjusted yearly for inflation. Transfers begin at about 15% of the average income of eligible families in the first six months after enrolment in CS, and gradually decline to about 10% of income by the end of the two years of home visits.

5For example, depending on the family structure, the transfer from Mexican Oportunidades may exceed $150 per month, and the Bolsa Familia monthly transfer in Brazil varies between $40-$60 per family.

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(i) re-directed the existing supply geographically, in proportion to the needs of CS families in each municipality; (ii) were tailored to the needs of the target population; and (iii) new programs were created.⁶ Additionally, the budget share allocated to the provision of programs to CS beneficiaries increased sixfold between 2003 and 2007 (Mideplan, 2009). As a result, the coverage of the potential demand⁷ for employment programs among CS beneficiaries increased from 24% in 2004 to 100% in 2007. To understand the impact of the supply adjustment on the effectiveness of CS we disaggregate our analysis by cohorts of entry, depending on whether families entered the program before or after 2004.

Selection of families, Coverage and Cost The targeting instrument used to select families to CS was the Ficha CAS between 2002 and 2006 (see section 4 for details about Ficha CAS).

From this instrument it is possible to construct the CAS score, according to which families are deemed eligible or not. The program was assigned geographically in proportion of the percentage of the population in extreme poverty in each municipality (P_c, estimated from the 2000 national household survey CASEN). Then, the official cutoff score of CAS for each municipality is the value of CAS such that the proportion of families below that CAS score within the municipality is exactly equal to P_c.

In order to be eligible, a family needs to have a CAS score. Therefore, in the initial stages of CS, there was an effort to register indigent families with the CAS system. However, the new registration occurred only in a few isolated instances (see Larra˜naga and Contreras, 2010). Due to capacity constraints not all eligible families were invited in the first year of operation. Thus, the initial plan was that 25% of all eligible families should be enrolled in CS in each year between 2002 and 2005, starting with families with lowest CAS values within the municipality. This sequencing implied that the cutoffs P_c were not binding in the first few of years of implementation of the program. Instead, within each municipality there was an effective threshold that varied across years. In section 3 we explain how this feature of the rollout of the program is used to identify its effects. Once invited, a family could reject or accept to participate. Acceptance was almost universal: out of all invited families only 4.7% did not participate (see table A.3 in the Appendix A).

3 Empirical Strategy

Our goal is to estimate β from the following equation:

Y_i = α + βCS_i+ f (X_i) + ε_i (1)

6See table A.2 in the Appendix A.

7Potential demand is defined as the number of households who have not met the corresponding minimum condition at entry to the program.

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where Yi is the outcome of interest for family i, CSi is a dummy variable indicating whether the family participated in Chile Solidario, X_i is a vector of controls (entering through function f (.)), and ε_i is an unobservable. β is the impact of the program on Y which, in principle, can vary across individuals. Even if β does not vary across individuals, the estimation of this equation by ordinary least squares (OLS) is problematic. Families who participate in CS are systematically different from those who do not in terms of their observable and unobservable characteristics.

On one end, participants in CS are indigent, and therefore they are on average much poorer than those who do not participate in CS. On the other end, not all indigent families participate in CS, and there may be differences between participants and non-participants among the indigents.

Families who live in more remote areas may be harder to visit, making them less likely to be invited to participate in CS. It could also happen that, among the eligible, those who participate are the ones more eager to improve their situation. In order to address these problems we use a regression discontinuity design, exploring the fact that the program eligibility rules imply that the probability that a household participates in CS is a discontinuous function of its CAS score.

A family is eligible for CS if its CAS score falls below a given cutoff, which varies across municipalities and time (as we explain below):

E_imt = 1[CAS_imt ≤ CAS_mt]

where E_imt is an indicator which takes value 1 if family i living in municipality m in year t is eligible for CS, CAS_imt is family i’s CAS score, and CAS_mt is the CS eligibility cutoff in municipality m at time t. In each municipality and time period, we compare outcomes of families just below (just eligible) and just above (just ineligible) their respective cutoffs (see, for example, Hahn et al., 2001;

Imbens and Lemieux, 2008; Lee and Lemieux, 2009).

An official set of CAS-cutoffs determining which families are eligible to the program was developed by the Ministry of Planning based on the income distribution in the municipality in 2000. As described in section 2, this cutoff was a function of the proportion of families who were found to be extreme poor in the national household survey carried out in 2000. We call this the official cutoff.

However, because of capacity constraints, CS was implemented gradually, targeting the poorest families first (those with the lowest CAS scores within each municipality), and then moving up in the CAS distribution. Thus, the first families to be served had a CAS score substantially below the official municipality cutoffs, which were not binding in the first years of the program.

In practice, the way the program was rolled out between 2002 and 2006 was roughly the following. Once the annual funding for CS was set for each municipality, the number of beneficiaries was defined for that year. Given that priority should be given to those families with the lowest CAS scores, a local cutoff could then be implicitly defined, as the CAS score below which the number of eligible families was equal to the number of potential beneficiaries fixed for the year.⁸

8In practice there was some slippage because some individuals with low CAS scores were often very hard to

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We call these the effective cutoffs (which are cohort and municipality specific). Over the years, the effective cutoffs converged to the official cutoffs.

Since these effective cutoffs are not observed, we follow a simple procedure proposed by Chay et al. (2005) to estimate them for each municipality and year of potential entry. This method searches across potential cutoff values for the one that best fits the participation data. The first step of this procedure is to construct different indicators of eligibility corresponding to different cutoff values for each municipality. Then, in each municipality, we regress participation in CS on eligibility. There is a separate regression for each potential cutoff value, defining a different potential eligibility variable. Finally, we define the effective cutoff for each municipality-year as the one that maximizes the fit of the regression.⁹

Figure B.1 in the Appendix B plots the distribution of estimated CS cutoffs across municipalities, for each year between 2002 and 2005. As expected, the distribution gradually shifted to the right over time. We show in section 5 that the effective cutoffs are much stronger determinants of participation than the official cutoffs. In 2002, the effective cutoff is higher than the official cutoff in 86.5% municipalities and in 2005 this proportion is reduced to 60%. The average difference between the effective and official cutoff is also very different across years. It drops from 16 points in 2002, to 2.9 points in 2005.¹⁰

Eligibility and Participation Many eligible families never enrol in CS. Table A.4 in Appendix A presents some of the main correlates of participation in CS, using only the sample of families who were eligible according to the official cutoff when they were first observed in the Ficha CAS (standard errors are clustered at the municipality level).

Families who are selected to CS are more likely to be connected to the welfare system, namely through the take-up of SUF. Within municipality, families who are selected to CS are less likely to have adequate walls or ceilings in their homes,¹¹ less likely to be legal occupants of their home, and more likely to have a connection to the sewage network. As expected, participant families have lower CAS scores than non participants, but heads and spouses in participant families are more likely to be working than those in non-participating families (perhaps indicating a strong motivation to improve their life conditions, which also leads them to enrol in CS). Selected families are more likely to have younger heads, married heads, female heads, and children. They are less likely to belong to the dominant ethnicity in the neighborhood, and to live in urban areas.

reach, so it was difficult to set a schedule of regular home visits as required by CS.

9Figure B.10 plots the average participation by vingtiles of the distribution of CAS of each municipality in 2002.

Although this figure includes only 25 municipalities in Chile the distributions presented are representative of what happened in the rest of the country. From this figure it is evident that the participation in CS is concentrated in the first two vingtiles of the CAS, with a sharp decline in participation thereafter.

10Figure B.2 plots the density of CAS-scores among the eligible families in the sample used in the regressions for families exposed to 2 years of CS, that is, those with CAS at most 20-points apart from the cutoff. The vertical lines in the figure are the 10th and 90th percentiles of the effective cutoffs. This figure shows the range of CAS over which we estimate the effects and the density of eligible families.

11See table A.5 for the definition of variables used.

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There are also some ineligible families who are able to benefit from CS. This means that the mapping from eligibility to participation in CS is not perfect. We address this problem by presenting instrumental variables estimates of the program computed as described in expression (2) (for very small ε):

lim

ε−→0⁺

Pr Y_i = 1|CAS_imt = CAS_mt− ε − lim

ε−→0⁺

Pr Y_i = 1|CAS_imt = CAS_mt+ ε lim

ε−→0⁺Pr CS_imt = 1|CAS_imt = CAS_mt− ε − lim

ε−→0⁺Pr CS_imt = 1|CAS_imt = CAS_mt+ ε . (2) Families just above and just below the cutoff differ in their eligibility to CS, but they are likely to be similar in all other (observable and unobservable) dimensions. All our comparisons of families in each side of the cutoff are done within municipality and time period. Our models include municipality-year effects, which absorb municipality-year shocks which may affect the outcome, independently of eligibility (for example, shocks in the local supply of social services, or shocks to the local labor market).

Once a family enrols in CS, it remains in the program for 5 years, even if its CAS score rises above the eligibility threshold during this period. This means that, at each period t, eligibility only determines participation for those not yet enrolled in CS. Therefore, for each year in which we measure eligibility we remove from the cohort of potential program entrants all families who are already enrolled in CS (because they are not affected by the eligibility cutoff in that year).

This means that our estimates are valid for a sample which is changing over time (which could be an important issue if program impacts vary substantially across families).

In regression discontinuity designs it is standard practice to restrict the sample to those families whose CAS is near the cutoff for the program, since points away from the discontinuity should have no weight in the estimation of program impacts (see e.g., Black, Galdo, and Smith, 2005, Lee and Lemieux, 2010). Thus, we focus on the sample of families whose CAS was at most 20 points apart of their municipality’s cutoff (we also present estimates using alternative bandwidths).

Finally, standard applications of regression discontinuity compare boundary points of (nonpara- metric) regressions of the outcome Y_i on CAS, estimated on each side of the discontinuity point.

Since we have several discontinuity points, one alternative (which we implement) is to normalize all of them to zero, and instead of the absolute value of CAS, consider instead CAS_im− CAS_m, which is the difference between a family’s CAS and the municipality cutoff in the relevant year.

We start by estimating the following model:

Y_imk = φ + γE_im+ f (CAS_im− CAS_m) + u_imk (3) where E_im is an indicator of eligibility for the program and u_imk is an idiosyncratic shock. We control for a non-linear function of CAS (normalized by the threshold). In practice, we use a quadratic in CAS_im− CAS_m, which can be different in either side of the cutoff, but we also

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present a robustness analysis using other parametric functions of distance to cutoff.

Then, we compute program impacts using a standard two-stage least squares procedure. All coefficients are estimated using a linear probability model in the first stage, where we regress a dummy variable indicating participation in CS on the eligibility dummy, controlling for distance to cutoff through f (CAS_im− CAS_m). In the second stage we estimate:

Y_imk = α + θCSd_imt−k+ g(CAS_im− CAS_m) + ε_imk (4) where k = 2, 4, 6 (which means that we study the effects of CS two to six years after the start of home visits), and participation at lag k is instrumented by eligibility for the program at lag k in their municipality of residence. Throughout the paper we refer interchangeably to the 2-year impacts as short run effects, the 4-year impacts as medium run effects and the 6-year impacts as long run effects (the latter are referred to in the paper but only presented in the appendix). All models include standard errors clustered at the municipality level (the municipality is measured at the time of eligibility).

One potential problem of equation (4) is that it ignores the evolution of the effective cutoffs within each municipality which followed the program roll out, and which means that families just ineligible in t may become eligible t + 1. As a result, our static IV estimates could be too small, because they ignore the fact that, over time, an increasing fraction of ineligible individuals is able to participate in CS. At the same time, it is also true that over time, the fraction of eligible individuals enrolled in the program may also change, which is again ignored when we take the static RD estimates at different points in time. In Appendix C we adapt the standard RD procedure to a dynamic version similar to Cellini, Ferreira and Rothstein (2010), to allow for the fact that individuals who do not receive CS in a given year may receive it in subsequent years. The results presented in section 5 show that the estimates produced in a static model are similar to those in the dynamic model.

Specification checks We perform a battery of checks to assess the validity of our empirical strategy. We start by performing standard balancing checks, by analyzing whether there are any differences between families just above and below the cutoffs in terms of variables measured before 2002.

Then, we show that our results are not driven by the choice of the functional form for f (CASimt−k− CAS_mt−k), nor they are sensitive to trimming the sample around cutoff and the choice of the bandwidth. We have similar results regardless of whether we control for interactive municipality-year effects, or whether we include only additive municipality and year effects, which suggests that municipality specific shocks are not likely to be correlated with how CS is rolled out across years.

Estimates are also similar if we include neighborhood fixed effects (neighborhoods are defined within municipalities). In our main set of estimates we restrict the sample to those families who

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were present in the CAS system prior to the introduction of CS (in 2000 or 2001), for whom we have pre-determined outcomes. Most of these robustness checks are included in Appendix A, but we refer to the most important ones in the main text.

4 Data

Our analysis is based on administrative data: the CAS Consolidado (for 2000-2006), Ficha de Proteccion Social (FPS) (for 2007-2009), and the registers of people participating in CS and other welfare programs. CAS Consolidado covered about one third of the Chilean population in 2006.

The FPS expanded the coverage from 2007 onward, reaching two thirds of the population in 2009.

These records include all families (and their members) applying to any publicly provided social program in Chile. We can link individuals across years through their national ID number (the RUN-Rol Unico Nacional), so our panel spans data from March 1998 to December 2009, covering over 14 million individuals, corresponding to nearly 60 million observations (see more details about the dataset in Appendix D). We have access to both the detailed information on the CAS and FPS forms, but also to the overall scores computed using that information. The scores are important to construct eligibility for CS.¹²

The Chilean national ID allows us to merge the CAS and the FPS to (i) the register of families participating in Chile Solidario since its inception until May 2009 and to (ii) the register of all individuals participating in social promotion and training programs offered by FOSIS¹³ between 2004 and 2007.

The government has been using the Ficha CAS as a targeting instrument since the 1980s. It consists of a two pages form that households must fill if they wish to apply for benefits. It contains information on housing conditions (e.g., material used for the construction of the house, access to water, sanitary services); characteristics of household members (occupation, educational level, date of birth, and income); and ownership of assets (housing property, refrigerator).¹⁴ This information is used to construct a score ranging from 380 to 770 points. Households with a CAS score below 500 are considered indigents, and those with a score between 500 and 540 are considered poor.

The CAS score is valid for 2 years. Up to 2007, the CAS-score was used to determine eligibility not only for income transfers (pension assistance for old age - PASIS, and family allowance - SUF), for the water subsidy (SAP), access to social housing, and childcare centers (Larra˜naga, 2005).

In 2007, the Ficha CAS was replaced by a new targeting instrument, the FPS. Given that the introduction of the new targeting mechanism was associated with new eligibility rules to CS

12The year of 2006 was a transition-year, and starting in 2007 eligibility to CS was based on a national threshold for a new score. Because of this change, in 2006 there were no families newly surveyed for a CAS score and the register contains about half the number families than in previous years.

13FOSIS stands for Fondo de Solidaridad e Inversion Social – Fund for Solidarity and Social Investment, which implements several programs in the areas of entrepreneurship, employment and social empowerment.

14See table D.1 in Appendix D for the 13 variables entering the CAS score.

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in this paper we do not focus on the effects for families that entered in CS in 2007 or after.

The information in FPS is administratively updated every month, using cross-checks with other administrative records. We obtained information taken in 3 dates: August 2007, December 2008 and December 2009.¹⁵

Construction of sample The final sample includes about 4.3 million families whose head is aged 18 to 75 in 2002 and who are observed at least once between 2002 and 2006 (some are observed between these years, and also in the FPS 2007-2009). We restrict our sample to families who we observe at least twice (in the year of potential entry, when eligibility is measure, and at least one additional year after that, when outcomes are measured). We are left with 2.7 million families after imposing this constraint. Finally, we restrict our main analysis to those families located at most 20 CAS-points apart of the eligibility thresholds, which implies that our main sample includes nearly 0.5 million families. Of these families, one third is observed twice, another one third is observed three times, 23% are observed 4 times, and the remaining families are observed 5 or more times between 2002 and 2009.

4.1 Descriptive Statistics

Table 1 includes some descriptive statistics, for the overall sample as well as for families who were ever eligible for CS. There is one observation per family in the table. We show the characteristics of families measured the first time they are observed in the data (2000, or 2001 if the family did not have a valid CAS score in 2000, before CS was implemented nationwide). We present separate statistics for the whole sample and for those families who are eligible to CS at least once between 2002 and 2006 according to the official cutoff in the municipality of residence. The information is divided into five areas: (1) use of subsidies, (2) housing characteristics, (3) variables related to CS, such as participant rate and CAS score, (4) employment and income related variables, and (5) demographic characteristics.

As expected, eligible families are more likely to be disadvantaged along multiple dimensions.

They have on average a lower CAS score and they are more likely to be receiving subsidies, and to be illegal occupants of the house where they live. Their houses are less likely to have adequate ceiling and walls, less likely to have water provided by the public network, less likely to have a fridge or to have water heating, and a higher density of occupation as measured by the ratio of

15Relatively to the CAS, the FPS is a more comprehensive instrument and it includes much more detailed information than the CAS on the labor market situation of each family member, and health and education. Information about durables and housing was mostly dropped from the FPS.

To understand the dynamics of entry in the data, we present in table D.2 a cross tab between the number of families in each wave against the first year the family has a valid survey. In each year between 2000 and 2005 there are around 1.5-1.8 millions families with a valid score (in 2006 there are only 0.7 million of families, since this was the year of transition to FPS). About 70% of the families with CAS valid in 2002 already had a valid score in either 2000 or 2001. Between 2000 and 2006 about 80% of the families requested the survey twice. This shows that there is some persistency of families in the system.

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persons in the house to the number of rooms. Eligible families also show a different employment profile than the general population: heads are less likely to be working, and, when working, they are more likely to be self-employed than the average individual (41% among eligible vs. 57%;

the alternative to self-employment is wage work). Spouses (of the head) are also less likely to be employed (13% among eligible vs. 24%). Finally, eligible families are on average younger, they have children, and are headed by individuals with below average education.

About half of the families who were present in the CAS in 2000/1, and who were ever eligible to CS (according to the official eligibility condition), ended up participating in the program.

4.2 Definition of Cohorts

The empirical strategy we lay out is clear in a static setting. However, our data is such that we observe families over several years. Each family can potentially enrol in CS in several years, or never at all.

Therefore, we define cohorts of potential entrants each year in the following way. Since 2002 is the first year of the program, every family who is in the CAS database in that year is a potential entrant, and it is labeled as belonging to the 2002 cohort. To define the 2003 cohort, we consider every family in the CAS database in that year, but who has not enrolled in CS in any prior year.

Past participants in CS should not be considered potential entrants into the program, and therefore we remove them from the sample. There are past CS participants on both sides of the set of CAS cutoff points in 2003.

If there were never new entrants into the CAS database, the families in the 2003 cohort would be a subset of families in the 2002 cohort. There are however entrants into the CAS database each year. Nevertheless there is still a large overlap in the set of families belonging to each cohort.

This does not mean that the overlap between the families in each cohort used in the estimation sample is equally large. The reason is that the cutoffs increase every year during the first 4 years of the program. Since we only take families with CAS scores contained within windows of 20 points on either side of the cutoff, it is possible that, for very large changes in cutoffs, there are substantial differences in the set of families used in the estimation of program impacts for each cohort (see Section 5.7).

When defining cohorts in subsequent years we proceed in an analogous way. In other words, we take all families who are in the CAS database in that year, and delete from the sample all those who have participated in CS in a prior year.

We estimate models with and without pooling all cohorts. When we pool them, we restrict the coefficients of the model to be the same across all cohorts.

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5 Results

5.1 Simple Statistics from Program Data

Before turning to our main empirical results, we use program data to document to what extent participants in CS are able to fulfil the minimum conditions discussed in section 2, during their time in the program. This data is produced by the social workers, who during their periodic visits to CS families, record whether each of the 53 minimum conditions is or not fulfilled.

Although we did not gain access to all the records produced in each visit by each social worker, we were able to access four snapshots of this register: December 2003, September 2004, September 2005, and August 2006. For each family in the program in each of these dates, we have information about the fulfillment of 47 out of the 53 minimum conditions. We also have the diagnostic performed in the first visit, which shows the extent to which the family fulfills these conditions at the time it enters the program (more details on this data are provided in the Appendix D).

Since different families have been in CS for different amounts of time in each of the four snapshots of data available to us, we can reorganize this data to compute the proportion of families fulfilling each of the minimum conditions when they first enter the program, and how this proportion evolves as families spend more time in CS. We plot this in figure B.3 in Appendix B. We consider measurements taken up to 36 months after entry into the program. In order to compare the progress on these outcomes comparable with our main RD analysis we restrict the sample to families whose CAS at entry in CS was at most 20-points apart from the cutoff.¹⁶ There is wide variation in the extent to which these minimum conditions are satisfied at entry (see also table A.1 in Appendix A). However, 36 months after program entry, it is striking how the proportion of households satisfying every one of them is very close to 1. This data suggests therefore, that CS is quite successful in improving the lives of its participants.

However, it is difficult from the raw data to separate the role of aggregate trends, differences across cohorts, and exposure to the program. Therefore, using this same sample, we estimate the following equation:

Y_{f mkt} = α +

36

X

t=0

θ_tT_{f mkt}+ f (CAS_{f mk}) + η_f + π_k+ τ_month+ ζ_m+ ν_{f mkt} (5)

where Y_{f mkt}is an indicator which is equal to 1 if a given minimum condition is fulfilled for family f , residing in municipality m when entered CS, k is the year of entry (2002 to 2006) and month is the month when the Puente data we have access to was recorded (August, September or December).

η_f is a family fixed effect. We also include indicators for the number of months since entry in Chile Solidario (T_{f mkt}), indicators for month of Puente survey (τ_month), cohort of entry (π_k) and

16Note that we observe the CAS-score of families at entry in CS.

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municipality of residence (ζm), and a cubic on CAS at entry (f (CASf mk))¹⁷. We run one for these regressions for each minimum condition.

Figure 1 plots our estimates of θ_t for 11 of the 47 minimum conditions for which we have data on. These conditions were chosen since they closely resemble some of our main outcome variables from Ficha CAS and FPS, namely take-up of public subsidies, employment and housing (see table A.5 in Appendix A; figure B.4 in Appendix B includes estimates for the 47 minimum conditions).

Identification of these parameters comes only from within family variation, although we assume that any underlying trends in the economy are common to all cohorts. The plots of figure 1 are suggestive about when to expect the largest changes in the the minimum conditions according to the period of exposure to the program. Regularization of housing tenure and access to clean water are minimum conditions that take the longest to be improved. Take-up of SUF and enrolment in the public health system exhibit the largest changes during the two years of psychosocial support with the health workers.

Although these results provide an interesting first image of the impacts of CS in the lives of the households, there are two important limitations to this data. First, this dataset only includes participants. It is still possible to look at the progression of each family within the CS program, and to remove other trends in the economy from this progression by exploring the fact that different families start in different time periods. But this can only be done under the assumption that these trends are common to all entry cohorts, which may not be quite true.

A perhaps more serious problem concerns the way this data is recorded. Whenever a minimum condition is fulfilled at a given point in time, the corresponding indicator becomes 1 in that period, and in all subsequent periods. Although we cannot verify this independently, it is plausible that even if a family fulfills a given minimum condition at a given point in time (for example, at least one household member works regularly), it may not be able to fulfill it in the future. However, in the data we never see such reversals. Therefore, the most accurate way to interpret each of our outcomes variables is not as an indicator of whether the minimum condition is satisfied at that point, but as an indicator of whether the minimum condition was ever satisfied at any date between the entry into CS and the current date, even if it is no longer satisfied at present. If that is the case, we are likely to overstate the positive impacts of the program by looking at this data.

We now turn to an alternative method to estimate program impacts (discussed in section 3), and also an alternative dataset (discussed in section 4). We are not able to study nearly as many outcomes, but we are able to provide robust estimates of the impact of CS on a smaller set of variables.

17The municipality fixed effects and controls in CAS at entry are subsumed by the family fixed effects.

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5.2 Eligibility and Participation in CS

We start by showing how eligibility for CS predicts participation in the program. Panel A of Figure 2 shows how the proportion of families participating in CS varies with the distance between each family’s CAS score and the municipality cutoff score for participation in CS. We present a plot for each of the cohorts of CS between 2002 and 2005 (2006 is an incomplete cohort as we mentioned in section 4, therefore we present only regression estimates for its first stage).

The dots in the figures correspond to cell means for participation in CS, after we divide the sample around the cutoff into groups. The groups are obtained by dividing the CAS values around the cutoff into bins of size 2. These are small bins in terms of the distribution of CAS (the mean CAS for this sample is 478, and its standard deviation is 36 for the sample around the cutoffs).

We consider only families with CAS scores within 20 points of each cutoff point, which means that there are 21 bins in total (11 to the left, and 10 to the right of the cutoff). The lines in each figure are local linear regressions estimates of an indicator of participation in CS on the distance to the effective cutoff, run separately for eligible (CAS_ijmt− CAS_mt ≤ 0) and ineligible (CASijmt− CASmt > 0) families (we use a bandwidth equal to 8). In each year, there is a clear discontinuity in participation in CS around the (normalized) cutoff. This means that program eligibility is a strong predictor of program participation.

Table 2 complements these figures, by showing estimates of equation (3), where the outcome variable (Y_imt) is an indicator for CS participation, and f (CAS_imt−k− CAS_mt−k) is a quadratic polynomial in its argument. In addition, we include municipality fixed effects, and run separate regressions for each year, so the variation we use is within municipality and year. There are 5 panels in the table, one for each cohort (2002-2006). For each cohort we present two columns.

The first one shows our estimate of the impact of eligibility on participation, where CAS_mt−k is the effective cutoff. The second shows the same estimate when we use the official cutoff for each municipality.

The discontinuities in the proportion of families enrolled in CS around the effective eligibility cutoff are large and statistically significant, ranging from 0.12 in 2002, to 0.22 to 2006. The discontinuities around the official cutoff are statistically significant, but much smaller in magnitude.

Panel B of Figure 2 which represents participation in CS as a function of distance to the official cutoff for different cohorts, also shows that for the first years of the operation of CS, eligibility as determined by official cutoff is a worse predictor of participation than eligibility determined by the effective cutoff. The bottom row of table 2 presents the F-statistic on the eligibility coefficients.

It shows that eligibility defined by the adjusted cutoffs is associated with a higher F-statistic than when eligibility is defined by the official cutoffs.

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5.3 Intent-to-Treat Estimates of Program Impacts

It is useful to start with simple intent-to-treat (ITT) estimates, because they can be read directly from figures showing outcomes as a function of the distance to the municipality’s cutoff. We investigate three groups of outcomes for which we have information in the Ficha CAS and the FPS: the take-up of subsidies and of employment programs, labor market outcomes, and housing conditions. We show program impacts measured 2 and 4 years after a family first enrolled in the program (in the Appendix we also present impacts measured 6 years after program enrolment, which can only be calculated for a restricted sample). In section 4.2 we allow the effects to vary by year of entry into the program. All variable definitions are given in table A.1 in the appendix.

The different panels in figures 3 and 4 show estimates of the relationship between outcomes and the distance to the municipality and cohort specific cutoffs, (CAS_im− CAS_m). The vertical line shows the point in the x-axis where this distance is equal to zero, i.e., the point of discontinuity.

Outcomes are measured two years after potential program enrolment (figure B.5 in Appendix presents similar figures but for outcomes measured four years after potential entry). The dots in the figures correspond to cell means for the outcomes after we divide the sample according to CAS scores into bins of size 2. The lines in the figures are local linear regressions estimates of the outcomes on the distance to the effective cutoff, separately for eligible (CAS_ijmt−CAS_mt≤ 0) and ineligible (CAS_ijmt− CAS_mt > 0) families.¹⁸ The figures also include 95% confidence intervals.

Figure 3 suggests that there is an increase in the take-up of SUF and SAP at the eligibility cutoff. We show below that the regression estimates are statistically significant for SUF,¹⁹ even though there is overlap in the pointwise confidence intervals on each side of the discontinuity.

The two middle panels in the figure concern the take-up of FOSIS (the employment programs), by either the head of the household or the spouse. They show an increase in the probability of participation in the employment programs at the cutoff, which is stronger for the head than for the spouse.²⁰ In the regressions below we can reject the null hypothesis that these impacts are equal to zero. Finally, the bottom panels concern the probability of legal ownership of the house, and access to public water networks. There is no statistically significant difference in these outcomes between families on either side of the discontinuity point.

Figure 4 concerns the employment status of head and spouse two years after entry in the program. We consider three mutually exclusive labor market states: not employed, self-employed, or wage worker. The panels on the left concern employment outcomes of the head of the household,

18We use a bandwidth equal to 8. We have also tried using bandwidths equal to 6 and 10, which resulted in fairly similar figures, see figures B.6 and B.7 in the appendix, respectively.

19The sample used for the impacts on SUF conditions on the presence of children in family before 2001, since poor families with children are the target of this subsidy. An additional requirement for the eligibility to SUF is that the family is not receiving Asignacion Familiar, which is assigned to children whose parents have Social Security. We do not observe this requirement in our data, but tabulations from CASEN 2003 show that 87% of CS participants do not receive Asignacion Familiar.

20We exclude participation in those programs which were especially created to serve members of families in CS.

See table A.2 in Appendix for the exact programs included.

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while those on the right concern the spouse. Although there are some differences in a few outcomes at the discontinuity point, none of them is statistically different from zero.

Table 3 presents estimates of γ in equation (3) for different outcomes (where, as above, f (CAS_im− CAS_m) is a quadratic polynomial in its argument, with different coefficients on each side of the cutoff. We include municipality-year specific fixed effects in all regressions. There are five columns in table 3. The first one shows the mean of the variable being considered for the sample of just ineligible families (with CAS scores at most 4 points above the cutoff). The second one shows ITT estimates measured 2 years after program enrolment (short run), corresponding to the results which were just presented in graphs. The fourth column consists of ITT estimates measured 4 years after enrolment (medium run). Columns (3) and (5) include the exact years of data used in the estimation. When we estimate longer-run impact estimates our sample size becomes smaller, because we only have data up to 2009. The stars next to each coefficient indicate whether it is statistically different from zero, after accounting for multiple hypothesis testing using the procedure in algorithms 4.1 and 4.2 of Romano and Wolf (2005).²¹

Table 3 shows that the strongest impacts of CS are on the take up of SUF, and of FOSIS (employment) programs for the spouse of the head. Although there are positive impact estimates in several other outcomes, they are not statistically different from zero once we adjust for multiple hypothesis testing. Furthermore, the positive impacts on the take-up of SUF and FOSIS programs are only statistically important in the short run. Below we show that, for particularly disadvantaged families, some of these impacts are sustained even in the medium run. Separating program impacts by type of family, according to their pre-program conditions, is very important, as shown in section 5.6.

It is reasonable that the strongest impacts are on the take-up of subsidies and social services, during the first two years, when home visits are in place. These are readily available to CS families, who are poor, and therefore eligible to receive them. In the first few visits to CS families, the social worker should be able to provide information about the programs and subsidies each family is entitled to, how they can benefit the family, and at the same time, help them register for these programs. In that sense, CS was able to significantly contribute to its main goal, which was an approximation of very poor families to the welfare system available to them. It is also natural to find that impacts on employment or housing are smaller, since these require more substantial shifts in individual behavior and use of other social programs.²²

21The critical values are adjusted for a two sided test. Throughout the paper we use 250 bootstrap replications to obtain the adjusted critical values.

22Additionally, the lack of effects on housing may reflect the strong constraints in the provision on support on this dimension (see Mideplan, 2010).

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5.4 Balancing Checks

In studies using regression discontinuity design it is standard to assess the extent to which there is balance in the observable characteristics of individuals in each side of the cutoff. Substantial imbalances may indicate that individuals were able to manipulate their score to be in the most favorable side of the discontinuity. Thus, we estimate equation (3) using as dependent variables pre-determined characteristics that should not be affected by the program (see Lee and Lemieux, 2010).

Table 4 shows the results for different variables (using the same specification as in table 3).

The table has 5 columns: one showing the mean of each variable for just ineligible families (column 1), columns 2 and 4 include the size of the sample used (which is the same for each outcome in the tables 3 and 4), column 3 presents the estimates with the sample used in the short run regressions, and column 5 uses the sample of the medium run regressions. All the outcome variables are measured either in 2000 (or 2001 if the family has no information for 2000), before CS was ever implemented.

There is no statistically significant estimate in this table after accounting for multiple hypothesis testing, suggesting that individuals located just below and just above each cutoff are similar in terms of observable pre-determined variables. Therefore, our empirical strategy is likely to be valid.²³

5.5 Instrumental Variables

We show in section 5.2 that eligibility to CS is a strong but imperfect predictor of participation in the program. At the cutoff, eligibility leads to an increase in the probability that a family participates in CS by 12 to 22 percentage points, depending on the year analyzed. Therefore, as discussed in section 3, the impacts of program participation are estimated by instrumental variables (IV).

Table 5 shows the IV estimates corresponding to the ITT estimates in table 3. Again, inference is adjusted for multiple hypothesis testing using the procedure in Romano and Wolf (2005). Table 5 includes IV estimates for short (columns 1 and 2) and medium run (columns 3 and 4) effects of the program.

The take-up of SUF by these families is fairly low, at 64.5%. We estimate that the probability that a family takes-up SUF increases by almost 11% two years after enrolment in CS. This is a large impact, but not enough to reach a 100% take-up rate.²⁴ There are substantial program

23The different panels of figure B.8 in Appendix show this graphically. Although some of the graphs suggest that there may be differences in some variables, they are not statistically different from zero. Furthermore, one of the few outcomes for which we found program impacts was SUF, and for this variable we have perfect balance. The only outcome for which this validation exercise cannot be performed is participation in employment programs from FOSIS prior to 2002, which is not available before 2004.

24As in any RD estimator, we are only able to identify program impacts for those families located near the

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impacts on the take-up of SUF measured 4 years after enrolment in the program, but they are not statistically different from zero.

The mean participation in employment (FOSIS) programs among non-eligible households is very low (below 2%), both for the head of household and for the spouse. Relative to these values, the magnitudes of program impacts in the short run on the take-up of these programs is very large:

2.3% for the head, and 3.9% for the spouse. Note that the take-up of employment programs is a lower bound estimate of the impact of the program, since the share of vacancies of such programs that were exclusively targeted to individuals in CS families increase over time since 2004. Impacts in the medium run are smaller and statistically insignificant.

For all other outcomes there are no statistically important impacts of CS on average. However, these average effects mask important heterogeneity of impact depending on the initial conditions and the cohorts of potential entry, which we study in the next section.²⁵

5.6 Differential Impacts Across Groups

In this section we show that there are substantial differences in program impacts across different types of families. We consider two dimensions of heterogeneity. First, we examine whether there are differential impacts for individuals who were in a vulnerable situation before participating in the program. Second, we examine whether there are differential impacts for individuals entering the program in different years, comparing the effects for those that (potential) enter CS before vs.

after the approval of the law that regulates the program in 2004.

Subsidies We start by dividing families according to whether they have any recorded access to subsidies before 2002. In particular, we examine the impacts of CS on SUF separately for families who took-up SUF in either 2000 or 2001 and for those who did not.²⁶ The reason for doing this is that the take-up of SUF before the existence of the program shows that family members have knowledge of the existence of the subsidy and its availability to the family. Furthermore, they are able to access it. It is possible that CS does not substantially impact SUF take-up for these families, while at the same time it has a large impact for those families for whom we have no past record of SUF take-up. The latter are more likely to be in a situation of isolation and exclusion

cutoffs. However, we have a fairly large range of cutoffs (as shown in figure B.1 in Appendix), the only families we are unable to span are extremely poor, with CAS values below 400 (the lowest cutoff in our data). This corresponds to 0.12% of families in the CAS registers.

25There could also be heterogeneity in impacts due to unobservables, which we ignore in this paper, and which is much discussed in the literature (e.g., Imbens and Angrist, 1994, Heckman and Vytlacil, 2005).

26The literature examining the take of social programs describes three leading causes of low take-up of social programs among the poor: lack of information about the program, high transaction costs, and stigma (Moffitt, 1983). Currie, 2006, puts emphasis on the costs of learning about and applying for a given program as a major deterrent for take-up of social programs. Currie’s review suggests that stigma plays a smaller role compared to other motives. Kleven and Kopczuk, 2011, model imperfect take-up as a response to program complexity and administrative hassle.